kotahi

Metadata

eLife Assessment

This paper undertakes an important investigation to determine whether movement slowing in microgravity is due to a strategic conservative approach or rather due to an underestimation of the mass of the arm. The experimental dataset is unique, the coupled experimental and computational analyses comprehensive, and the effect is strong. However, the authors present incomplete results to support the claim that movement slowing is due to mass underestimation. Further analysis is needed to rule out alternative explanations.

Reviewer #1 (Public review):

The authors have conducted substantial additional analyses to address the reviewers' comments. However, several key points still require attention. I was unable to see the correspondence between the model predictions and the data in the added quantitative analysis. In the rebuttal letter, the delta peak speed time displays values in the range of [20, 30] ms, whereas the data were negative for the 45{degree sign} direction. Should the reader directly compare panel B of Figure 6 with Figure 1E? The correspondence between the model and the data should be made more apparent in Figure 6. Furthermore, the rebuttal states that a quantitative prediction was not expected, yet it subsequently argues that there was a quantitative match. Overall, this response remains unclear.

A follow-up question concerns the argument about strategic slowing. The authors argue that this explanation can be rejected because the timing of peak speed should be delayed, contrary to the data. However, there appears to be a sign difference between the model and the data for the 45{degree sign} direction, which means that it was delayed in this case. Did I understand correctly? In that regard, I believe that the hypothesis of strategic slowing cannot yet be firmly rejected and the discussion should more clearly indicate that this argument is based on some, but not all, directions. I agree with the authors on the importance of the mass underestimation hypothesis, and I am not particularly committed to the strategic slowing explanation, but I do not see a strong argument against it. If the conclusion relies on the sign of the delta peak speed, then the authors' claims are not valid across all directions, and greater caution in the interpretation and discussion is warranted. Regarding the peak acceleration time, I would be hesitant to draw firm conclusions based on differences smaller than 10 ms (Figures R3 and 6D).

The authors state in the rebuttal that the two hypotheses are competing. This is not accurate, as they are not mutually exclusive and could even vary as a function of movement direction. The abstract also claims that the data "refutes" strategic slowing, which I believe is too strong. The main issue is that, based on the authors' revised manuscript, the lack of quantitative agreement between the model and the data for the mass underestimation hypothesis is considered acceptable because a precise quantitative match is not expected, and the predictions overall agree for some (though not all) directions and phases (excluding post-in). That is reasonable, but by the same logic, the small differences between the model prediction and the strategic slowing hypothesis should not be taken as firm evidence against it, as the authors seem to suggest. In practice, I recommend a more transparent and cautious interpretation to avoid giving readers the false impression that the evidence is decisive. The mass underestimation hypothesis is clearly supported, but the remaining aspects are less clear, and several features of the data remain unexplained.

Reviewer #2 (Public review):

This study explores the underlying causes of the generalized movement slowness observed in astronauts in weightlessness compared to their performance on Earth. The authors argue that this movement slowness stems from an underestimation of mass rather than a deliberate reduction in speed for enhanced stability and safety.

Overall, this is a fascinating and well-written work. The kinematic analysis is thorough and comprehensive. The design of the study is solid, the collected dataset is rare, and the model adds confidence to the proposed conclusions.

Compared to the previous version, the authors have thoroughly addressed my concerns. The model is now clear and well-articulated, and alternative hypotheses have been ruled out convincingly. The paper is improved and suitable for publication in my opinion, making a significant contribution to the field.

Strengths:

- Comprehensive analysis of a unique data set of reaching movement in microgravity
- Use of a sensible and well-thought experimental approach
- State-of-the-art analyses of main kinematic parameter
- Computational model simulations of arm reaching to test alternative hypotheses and support the mass underestimation one

This work has no major weakness as it stands, and the discussion provides a fair evaluation of the findings and conclusions.

Reviewer #3 (Public review):

Summary:

The authors describe an interesting study of arm movements carried out in weightlessness after a prolonged exposure to the so-called microgravity conditions of orbital spaceflight. Subjects performed radial point-to-point motions of the fingertip on a touch pad. The authors note a reduction in movement speed in weightlessness, which they hypothesize could be due to either an overall strategy of lowering movement speed to better accommodate the instability of the body in weightlessness or an underestimation of body mass. They conclude for the latter, mainly based on two effects. One, slowing in weightlessness is greater for movement directions with higher effective mass at the end effector of the arm. Two, they present evidence for increased number of corrective submovements in weightlessness. They contend that this provides conclusive evidence to accept the hypothesis of an underestimation of body mass.

Strengths:

In my opinion, the study provides a valuable contribution, the theoretical aspects are well presented through simulations, the statistical analyses are meticulous, the applicable literature is comprehensively considered and cited and the manuscript is well written.

Weaknesses:

I nevertheless am of the opinion that the interpretation of the observations leaves room for other possible explanations of the observed phenomenon, thus weakening the strength of the arguments.

To strengthen the conclusions, I feel that the following points would need to be addressed:

(1) The authors model the movement control through equations that derive the input control variable in terms of the force acting on the hand and treating the arm as a second-order low pass filter (Eq. 13). Underestimation of the mass in the computation of a feedforward command would lead to a lower-than-expected displacement to that command. But it is not clear if and how the authors account for a potential modification of the time constants of the 2nd order system. The CNS does not effectuate movements with pure torque generators. Muscles have elastic properties that depend on their tonic excitation level, reflex feedback and other parameters. Indeed, Fisk et al.* showed variations of movement characteristics consistent with lower muscle tone, lower bandwidth and lower damping ratio in 0g compared to 1g. Could the variations in the response to the initial feedforward command be explained by a misrepresentation of the limbs damping and natural frequency, leading to greater uncertainty to the consequences of the initial command. This would still be an argument for un-adapted feedforward control of the movement, leading to the need for more corrective movements. But it would not necessarily reflect an underestimation of body mass.

*Fisk, J. O. H. N., Lackner, J. R., & DiZio, P. A. U. L. (1993). Gravitoinertial force level influences arm movement control. Journal of neurophysiology, 69(2), 504-511.

While the authors attempt to differentiate their study from previous studies where limb neuromechanical impedance was shown to be modified in weightlessness by emphasizing that in the current study the movements were rapid and the initial movement is "feedforward". But this incorrectly implies that the limb's mechanical response to the motor command is determined only by active feedback mechanisms. In fact:

(a) All commands to the muscle pass through the motor neurons. These neurons receive descending activations related not only to the volitional movement, but also to the dynamic state of the body and the influence of other sensory inputs, including the vestibular system. A decrease in descending influences from the vestibular organs will lower the background sensitivity to all other neural influences on the motor neuron. Thus, the motor neuron may be less sensitive to the other volitional and reflexive synaptic inputs that it may receive.

(b) Muscle tone plays a significant role in determining the force and the time course of the muscle contraction. In a weightless environment, where tonic muscle activity is likely to be reduced, there is the distinct possibility that muscles will react more slowly and with lower amplitude to an otherwise equivalent descending motor command, particularly in the initial moments before spinal reflexes come into play. These, and other neuronal mechanisms could lead to the "under-actuation" effect observed in the current study, without necessarily being reflective of an underestimation of mass per se.

(2) The subject's body in weightless is much more sensitive to reaction forces in interactions with the environment in the absence of the anchoring effect of gravity pushing the body into the floor and in the absence of anticipatory postural adjustments that typically accompany upper-limb motions in Earth gravity in order to maintain an upright posture. The authors dismiss this possibility because the taikonauts were asked to stabilize their bodies with the contralateral hand. But the authors present no evidence that this was sufficient to maintain the shoulder and trunk at a strictly constant position, as is supposed by the simplified biomechanical model used in their optimal control framework. Indeed, a small backward motion of the shoulder would result in a smaller acceleration of the fingertip and a smaller extent of the initial ballistic motion of the hand with respect to the measurement device (the tablet), consistent with the observations reported in the study. Note that stability of the base might explain why 45º movements were apparently less affected in weightlessness, according to many of the reported analyses, including those related to corrective movements (Fig. 5 B, C, F; Fig. 6D), than the other two directions. If the trunk is being stabilized by the left arm, the same reaction forces on the trunk due to the acceleration of the hand will result in less effective torque on the trunk, given that the reaction forces act with a much smaller moment arm with respect to the left shoulder (the hand movement axis passes approximately through the left shoulder for the 45º target) compared to either the forward or rightward motions of the hand.

(3) The above is exacerbated by potential changes in the frictional forces between the fingertip and the tablet. The movements were measured by having the subjects slide their finger on the surface of a touch screen. In weightlessness, the implications of this contact can be expected to be quite different than on the ground. While these forces may be low on Earth, the fact is that we do not know what forces the taikonauts used on orbit. In weightlessness, the taikonauts would need to actively press downward to maintain contact with the screen, while on Earth gravity will do the work. The tangential forces that resist movement due to friction might therefore be different in 0g. . Indeed, given the increased instability of the body and the increased uncertainty of movement direction of the hand, taikonauts may have been induced to apply greater forces against the tablet in order to maintain contact in weightlessness, which would in turn slow the motion of the finger on the table and increase the reaction forces acting on the trunk. This could be particularly relevant given that the effect of friction would interact with the limb in a direction-dependent fashion, given the anisotropy of the equivalent mass at the fingertip evoked by the authors

I feel that the authors have done an admirable job of exploring the how to explain the modifications to movement kinematics that they observed on orbit within the constraints of the optimal control theory applied to a simplified model of the human motor system. While I fully appreciate the value of such models to provide insights into question of human sensorimotor behaviour, to draw firm conclusions on what humans are actually experiencing based only on manipulations of the computational model, without testing the model's implicit assumptions and without considering the actual neurophysiological and biomechanical mechanisms, can be misleading. One way to do this could be to examine these questions through extensions to the model used in the simulations (changing activation dynamics of the torque generators, allowing for potential motion backward motion of the shoulder and trunk, etc.). A better solution would be to emulate the physiological and biomechanical conditions on Earth (supporting the arm against gravity to reduce muscle tone, placing the subject on a moveable base that requires that the body be stabilized with the other hand) in order to distinguish the hypothesis of an underestimation of mass vs. other potential sources of under-actuation and other potential effects of weightlessness on the body.

In sum, my opinion is that the authors are relying too much on a theoretical model as a ground truth and thus overstate their conclusions. But to provide a convincing argument that humans truly underestimate mass in weightlessness, they should consider more judiciously the neurophysiology and biomechanics that fall outside the purview of the simplified model that they have chosen. If a more thorough assessment of this nature is not possible, then I would argue that a more measured conclusion of the paper should be 1) that the authors observed modifications to movement kinematics in weightlessness consistent with an under-actuation for the intended motion, 2) that a simplified model of human physiology and biomechanics that incorporates principles of optimal control suggest that the source of this under-actuation might be an underestimation of mass in the computation of an appropriate feedforward motor command, and 3) that other potential neurophysiological or biomechanical effects cannot be excluded due to limitations of the computational model.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This paper undertakes an important investigation to determine whether movement slowing in microgravity is due to a strategic conservative approach or rather due to an underestimation of the mass of the arm. While the experimental dataset is unique and the coupled experimental and computational analyses comprehensive, the authors present incomplete results to support the claim that movement slowing is due to mass underestimation. Further analysis is needed to rule out alternative explanations.

We thank the editor and reviewers for the thoughtful and constructive comments, which helped us substantially improve the manuscript. In this revised version, we have made the following key changes:

- Directly presented the differential effect of microgravity in different movement directions, showing its quantitative match with model predictions.

- Showed that changing cost function with the idea of conservative strategy is not a viable alternative.

- Showed our model predictions remain largely the same after adding Coriolis and centripetal torques.

- Discussed alternative explanations including neuromuscular deconditioning, friction, body stability, etc.

- Detailed the model description and moved it to the main text, as suggested.

Our point-to-point response is numbered to facilitate cross-referencing.

We believe the revisions and the responses adequately addresses the reviewers’ concerns, and new analysis results strengthened our conclusion that mass underestimation is the major contributor to movement slowing in microgravity.

Reviewer #1 (Public review):
Summary:
This article investigates the origin of movement slowdown in weightlessness by testing two possible hypotheses: the first is based on a strategic and conservative slowdown, presented as a scaling of the motion kinematics without altering its profile, while the second is based on the hypothesis of a misestimation of effective mass by the brain due to an alteration of gravity-dependent sensory inputs, which alters the kinematics following a controller parameterization error.

Strengths:
The article convincingly demonstrates that trajectories are affected in 0g conditions, as in previous work. It is interesting, and the results appear robust. However, I have two major reservations about the current version of the manuscript that prevent me from endorsing the conclusion in its current form.

Weaknesses:
(1) First, the hypothesis of a strategic and conservative slow down implicitly assumes a similar cost function, which cannot be guaranteed, tested, or verified. For example, previous work has suggested that changing the ratio between the state and control weight matrices produced an alteration in movement kinematics similar to that presented here, without changing the estimated mass parameter (Crevecoeur et al., 2010, J Neurophysiol, 104 (3), 1301-1313). Thus, the hypothesis of conservative slowing cannot be rejected. Such a strategy could vary with effective mass (thus showing a statistical effect), but the possibility that the data reflect a combination of both mechanisms (strategic slowing and mass misestimation) remains open.

Response (1): Thank you for raising this point. The basic premise of this concern is that changing the cost function for implementing strategic slowing can reproduce our empirical findings, thus the alternative hypothesis that we aimed to refute in the paper remain possible. At least, it could co-exist with our hypothesis of mass underestimation. In the revision, we show that changing the cost function only, as suggested here, cannot produce the behavioral patterns observed in microgravity.

As suggested, we modified the relative weighting of the state and control cost matrices (i.e., Q and R in the cost function Eq 15) without considering mass underestimation. While this cost function scaling can decrease peak velocity – a hallmark of strategic slowing – it also inevitably leads to later peak timings. This is opposite to our robust findings: the taikonauts consistently “advanced” their peak velocity and peak acceleration in time. Note, these model simulation patterns have also been shown in Crevecoeur et al. (2010), the paper mentioned by the reviewer (see their Figure 7B).

We systematically changed the ratio between the state and control weight matrices in the simulation, as suggested. We divided Q and multiplied R by the same factor α, the cost function scaling parameter α as defined in Crevecoeur et al. (2010). This adjustment models a shift in movement strategy in microgravity, and we tested a wide range of α to examine reasonable parameter space. Simulation results for α = 3 and α = 0.3 are shown in Figure 1—figure supplement 2 and Figure 1—figure supplement 3 respectively. As expected, with α = 3 (higher control effort penalty), peak velocities and accelerations are reduced, but their timing is delayed. Conversely, with α = 0.3, both peak amplitude and timing increase. Hence, changing the cost function to implement a conservative strategy cannot produce the kinematic pattern observed in microgravity, which is a combination of movement slowing and peak timing advance.

Therefore, we conclude that a change in optimal control strategy alone is insufficient to explain our empirical findings. Logically speaking, we cannot refute the possibility of strategic slowing, which can still exist on top of the mass underestimation we proposed here. However, our data does not support its role in explaining the slowing of goal-directed hand reaching in microgravity. We have added these analyses to the Supplementary Materials and expanded the Discussion to address this point.

(2) The main strength of the article is the presence of directional effects expected under the hypothesis of mass estimation error. However, the article lacks a clear demonstration of such an effect: indeed, although there appears to be a significant effect of direction, I was not sure that this effect matched the model's predictions. A directional effect is not sufficient because the model makes clear quantitative predictions about how this effect should vary across directions. In the absence of a quantitative match between the model and the data, the authors' claims regarding the role of misestimating the effective mass remain unsupported.

Response (2): First, we have to clarify that our study does not aim to quantitatively fit observed hand trajectory. The two-link arm model simulates an ideal case of moving a point mass (effective mass) on a horizontal plane without friction (Todorov, 2004; 2005). In contrast, in the experiment, participants moved their hand on a tabletop without vertical arm support, so the movement was not strictly planar and was affected by friction. Thus, this kind of model can only illustrate qualitative differences between conditions, as in the majorities of similar modeling studies (e.g., Shadmehr et al., 2016). In our study, qualitative simulation means the model is intended to reproduce the directional differences between conditions—not exact numeric values—in key kinematic measures. Specifically, it should capture how the peak velocity and acceleration amplitudes and their timings differ between normal gravity and microgravity (particularly under the mass-underestimation assumption).

Second, the reviewer rightfully pointed out that the directional effect is essential for our theorization of the importance of mass underestimation. However, the directional effect has two aspects, which were not clearly presented in our original manuscript. We now clarify both here and in the revision. The first aspect is that key kinematic variables (peak velocity/acceleration and their timing) are affected by movement direction, even before any potential microgravity effect. This is shown by the ranking order of directions for these variables (Figure 1C-H). The direction-dependent ranking, confirmed by pre-flight data, indicates that effective mass is a determining factor for reaching kinematics, which motivated us to study its role in eliciting movement slowing in space. This was what our original manuscript emphasized and clearly presented.

The second aspect is that the hypothetical mass underestimation might also differentially affect movements in different directions. This was not clearly presented in the original manuscript. However, we would not expect a quantitative match between model predictions and empirical data, for the reasons mentioned above. We now show this directional ranking in microgravity-elicited kinematic changes in both model simulations and empirical data. The overall trend is that the microgravity effect indeed differs between directions, and the model predictions and the data showed a reasonable qualitative match (Author response image 1 below).

Shown in Author response image 1, we found that for amplitude changes (Δ peak speed, Δ peak acceleration) both the model and the mean of empirical data show the same directional ordering (45° > 90° > 135°) in pre-in and post-in comparisons. For timing (Δ peak-speed time, Δ peak-acceleration time), which we consider the most diagnostic, the same directional ranking was observed. We only found one deviation, i.e., the predicted sign (earlier peaks) was confirmed at 90° and 135°, but not at 45°. As discussed in Response (6), the absence of timing advance at 45° may reflect limitations of our simplified model, which did not consider that the 45° direction is essentially a single-joint reach. Taken together, the directional pattern is largely consistent with the model predictions based on mass underestimation. The model successfully reproduces the directional ordering of amplitude measures -- peak velocity and peak acceleration. It also captures the sign of the timing changes in two out of the three directions. We added these new analysis results in the revision and expanded Discussion accordingly.

The details of our analysis on directional effects: We compared the model predictions (Author response image 1, left) with the experimental data (Author response image 1, right) across the three tested directions (45°, 90°, 135°). In the experimental data panels, both Δ(pre-in) (solid bars) and Δ(post-in) (semi-transparent bars) with standard error are shown. The directional trends are remarkably similar between model prediction and actual data. The post-in comparison is less aligned with model prediction; we postulate that the incomplete after-flight recovery (i.e., post data had not returned to pre-flight baselines) might obscure the microgravity effect. Incomplete recovery has also been shown in our original manuscript: peak speed and peak acceleration did not fully recover in post-flight sessions when compared to pre-flight sessions. To further quantify the correspondence between model and data, we performed repeated-measures correlation (rm-corr) analyses. We found significant within-subject correlations for three of the four metrics. For pre–in, Δ peak speed time (rrm = 0.627, t(23) = 3.858, p < 0.001), Δ peak acceleration time (rrm = 0.591, t(23) = 3.513, p = 0.002), and Δ peak acceleration (rrm = 0.573, t(23) = 3.351, p = 0.003) were significant, whereas Δ peak speed was not (rrm = 0.334, t(23) = 1.696, p = 0.103). These results thus show that the directional effect, as predicted our model, is observed both before spaceflight and in spaceflight (the pre-in comparison).

Author response image 1.

Directional comparison between model predictions and experimental data across the three reach directions (45°, 90°, 135°). Left: model outputs. Right: experimental data shown as Δ relative to the in-flight session; solid bars = Δ(in − pre) and semi-transparent bars = Δ(in − post). Colors encode direction consistently across panels (e.g., 45° = darker hue, 90° = medium, 135° = lighter/orange). Panels (clockwise from top-left): Δ peak speed (cm/s), Δ peak speed time (ms), Δ peak acceleration time (ms), and Δ peak acceleration (cm/s²). Bars are group means; error bars denote standard error across participants.

Citations:

Todorov, E. (2004). Optimality principles in sensorimotor control. Nature Neuroscience, 7(9), 907.

Todorov, E. (2005). Stochastic optimal control and estimation methods adapted to the noise characteristics of the sensorimotor system. Neural Computation, 17(5), 1084–1108.

Shadmehr, R., Huang, H. J., & Ahmed, A. A. (2016). A Representation of Effort in Decision-Making and Motor Control. Current Biology: CB, 26(14), 1929–1934.

In general, both the hypotheses of slowing motion (out of caution) and misestimating mass have been put forward in the past, and the added value of this article lies in demonstrating that the effect depended on direction. However, (1) a conservative strategy with a different cost function can also explain the data, and (2) the quantitative match between the directional effect and the model's predictions has not been established.

We agree that both hypotheses have been put forward before, however they are competing hypotheses that have not been resolved. Furthermore, the mass underestimation hypothesis is a conjecture without any solid evidence; previous reports on mass underestimation of object cannot directly translate to underestimation of body. As detailed in our responses above, we have shown that a conservative strategy implemented via a different cost function cannot reproduce the key findings in our dataset, thereby supporting the alternative hypothesis of mass underestimation. Moreover, we found qualitative agreement between the model predictions and the experimental data in terms of directional effects, which further strengthens our interpretation.

Specific points:
(1) I noted a lack of presentation of raw kinematic traces, which would be necessary to convince me that the directional effect was related to effective mass as stated.

Response (3): We are happy to include exemplary speed and acceleration trajectories. Kinematic profiles from one example participant are shown in Figure 2—figure supplement 6.

(2) The presentation and justification of the model require substantial improvement; the reason for their presence in the supplementary material is unclear, as there is space to present the modelling work in detail in the main text. Regarding the model, some choices require justification: for example, why did the authors ignore the nonlinear Coriolis and centripetal terms?

Response (4): Great suggestion. In the revision, we have moved the model into the main text and added further justification for using this simple model.

We initially omitted the nonlinear Coriolis and centripetal terms in order to start with a minimal model. Importantly, excluding these terms does not affect the model’s main conclusions. In the revision we added simulations that explicitly include these terms. The full explanation and simulations are provided in the Supplementary Notes 2 (this time we have to put it into the Supplementary to reduce the texts devoted to the model). More explanations can also be found in our response to Reviewer 2 (response (6)). The results indicate that, although these velocity-dependent forces show some directional anisotropy, their contribution is substantially smaller relative to that of the included inertial component; specifically, they have only a negligible impact on the predicted peak amplitudes and peak times.

(3) The increase in the proportion of trials with subcomponents is interesting, but the explanatory power of this observation is limited, as the initial percentage was already quite high (from 60-70% during the initial study to 70-85% in flight). This suggests that the potential effect of effective mass only explains a small increase in a trend already present in the initial study. A more critical assessment of this result is warranted.

Response (5): Thank you for your thoughtful comment. You are correct that the increase in the percentage of trials with submovements is modest, but a more critical change was observed in the timing between submovement peaks—specifically, the inter-peak interval (IPI). These intervals became longer during flight. Taken together with the percentage increase, the submovement changes significantly predicted the increase in movement duration, as shown by our linear mixed-effects model, which indicated that IPI increased.

Reviewer #2 (Public review):
This study explores the underlying causes of the generalized movement slowness observed in astronauts in weightlessness compared to their performance on Earth. The authors argue that this movement slowness stems from an underestimation of mass rather than a deliberate reduction in speed for enhanced stability and safety.
Overall, this is a fascinating and well-written work. The kinematic analysis is thorough and comprehensive. The design of the study is solid, the collected dataset is rare, and the model tends to add confidence to the proposed conclusions. That being said, I have several comments that could be addressed to consolidate interpretations and improve clarity.

Main comments:
(1) Mass underestimation
a) While this interpretation is supported by data and analyses, it is not clear whether this gives a complete picture of the underlying phenomena. The two hypotheses (i.e., mass underestimation vs deliberate speed reduction) can only be distinguished in terms of velocity/acceleration patterns, which should display specific changes during the flight with a mass underestimation. The experimental data generally shows the expected changes but for the 45° condition, no changes are observed during flight compared to the pre- and post-phases (Figure 4). In Figure 5E, only a change in the primary submovement peak velocity is observed for 45°, but this finding relies on a more involved decomposition procedure. It suggests that there is something specific about 45° (beyond its low effective mass). In such planar movements, 45° often corresponds to a movement which is close to single-joint, whereas 90° and 135° involve multi-joint movements. If so, the increased proportion of submovements in 90° and 135° could indicate that participants had more difficulties in coordinating multi-joint movements during flight. Besides inertia, Coriolis and centripetal effects may be non-negligible in such fast planar reaching (Hollerbach & Flash, Biol Cyber, 1982) and, interestingly, they would also be affected by a mass underestimation (thus, this is not necessarily incompatible with the author's view; yet predicting the effects of a mass underestimation on Coriolis/centripetal torques would require a two-link arm model). Overall, I found the discrepancy between the 45° direction and the other directions under-exploited in the current version of the article. In sum, could the corrective submovements be due to a misestimation of Coriolis/centripetal torques in the multi-joint dynamics (caused specifically -or not- by a mass underestimation)?

Response (6): Thank you for raising these important questions. We unpacked the whole paragraph into two concerns: 1) the possibility that misestimation of Coriolis and centripetal torques might lead to corrective submovements, and 2) the weak effect in the 45° direction unexploited. These two concerns are valid but addressable, and they did not change our general conclusions based on our empirical findings (see Supplementary note 2. Coriolis and centripetal torques have minimal impact).

Possible explanation for the 45° discrepancy

We agree with the reviewer that the 45° direction likely involves more single-joint (elbow-dominant) movement, whereas the 90° and 135° directions require greater multi-joint (elbow + shoulder) coordination. This is particularly relevant when the workspace is near body midline (e.g., Haggard & Richardson, 1995), as the case in our experimental setup. To demonstrate this, we examined the curvature of the hand trajectories across directions. Using cumulative curvature (positive = counterclockwise), we obtained average values of 6.484° ± 0.841°, 1.539° ± 0.462°, and 2.819° ± 0.538° for the 45°, 90°, and 135° directions, respectively. The significantly larger curvature in the 45° condition suggests that these movements deviate more from a straight-line path, a hallmark of more elbow-dominant movements.

Importantly, this curvature pattern was present in both the pre-flight and in-flight phases, indicating that it is a general movement characteristic rather than a microgravity-induced effect. Thus, the 45° reaches are less suitable for modeling with a simplified two-link arm model compared to the other two directions. We believe this is the main reason why the model predictions based on effective mass become less consistent with the empirical data for the 45° direction.

We have now incorporated this new analysis in the Results and discussed it in the revised Discussion.

Citation: Haggard, P., Hutchinson, K., & Stein, J. (1995). Patterns of coordinated multi-joint movement. Experimental Brain Research, 107(2), 254-266.

b) Additionally, since the taikonauts are tested after 2 or 3 weeks in flight, one could also assume that neuromuscular deconditioning explains (at least in part) the general decrease in movement speed. Can the authors explain how to rule out this alternative interpretation? For instance, weaker muscles could account for slower movements within a classical time-effort trade-off (as more neural effort would be needed to generate a similar amount of muscle force, thereby suggesting a purposive slowing down of movement). Therefore, could the observed results (slowing down + more submovements) be explained by some neuromuscular deconditioning combined with a difficulty in coordinating multi-joint movements in weightlessness (due to a misestimation or Coriolis/centripetal torques) provide an alternative explanation for the results?

Response (7): Neuromuscular deconditioning is indeed a space effect; thanks for bringing this up as we omitted the discussion of this confounds in our original manuscript. Prolonged stay in microgravity can lead to a reduction of muscle strength, but this is mostly limited to lower limb. For example, a recent well-designed large-sample study have shown that while lower leg muscle showed significant strength reductions, no changes in mean upper body strength was found (Scott et al., 2023), consistent with previous propositions that muscle weakness is less for upper-limb muscles than for postural and lower-limb muscles (Tesch et al., 2005). Furthermore, the muscle weakness is unlikely to play a major role here since our reaching task involves small movements (~12cm) with joint torques of a magnitude of ~2N·m. Of course, we cannot completely rule out the contribution of muscle weakness; we can only postulate, based on the task itself (12 cm reaching) and systematic microgravity effect (the increase in submovements, the increase in the inter-submovements intervals, and their significant prediction on movement slowing), that muscle weakness is an unlikely major contributor for the movement slowing.

The reviewer suggests that poor coordination in microgravity might contribute to slowing down + more submovements. This is also a possibility, but we did not find evidence to support it. First, there is no clear evidence or reports about poor coordination for simple upper-limb movements like reaching investigated here. Note that reaching or aiming movement is one of the most studied tasks among astronauts. Second, we further analyzed our reaching trajectories and found no sign of curvature increase, a hallmark of poor coordination of Coriolis/centripetal torques, in our large collection of reaching movements. We probably have the largest dataset of reaching movements collected in microgravity thus far, given that we had 12 taikonauts and each of them performed about 480 to 840 reaching trials during their spaceflight. We believe the probability of Type II error is quite low here.

Citation: Tesch, P. A., Berg, H. E., Bring, D., Evans, H. J., & LeBlanc, A. D. (2005). Effects of 17-day spaceflight on knee extensor muscle function and size. European journal of applied physiology, 93(4), 463-468.

Scott J, Feiveson A, English K, et al. Effects of exercise countermeasures on multisystem function in long duration spaceflight astronauts. npj Microgravity. 2023;9(11).

(2) Modelling
a) The model description should be improved as it is currently a mix of discrete time and continuous time formulations. Moreover, an infinite-horizon cost function is used, but I thought the authors used a finite-horizon formulation with the prefixed duration provided by the movement utility maximization framework of Shadmehr et al. (Curr Biol, 2016). Furthermore, was the mass underestimation reflected both in the utility model and the optimal control model? If so, did the authors really compute the feedback control gain with the underestimated mass but simulate the system with the real mass? This is important because the mass appears both in the utility framework and in the LQ framework. Given the current interpretations, the feedforward command is assumed to be erroneous, and the feedback command would allow for motor corrections. Therefore, it could be clarified whether the feedback command also misestimates the mass or not, which may affect its efficiency. For instance, if both feedforward and feedback motor commands are based on wrong internal models (e.g., due to the mass underestimation), one may wonder how the astronauts would execute accurate goal-directed movements.

b) The model seems to be deterministic in its current form (no motor and sensory noise). Since the framework developed by Todorov (2005) is used, sensorimotor noise could have been readily considered. One could also assume that motor and sensory noise increase in microgravity, and the model could inform on how microgravity affects the number of submovements or endpoint variance due to sensorimotor noise changes, for instance.

c) Finally, how does the model distinguish the feedforward and feedback components of the motor command that are discussed in the paper, given that the model only yields a feedback control law? Does 'feedforward' refer to the motor plan here (i.e., the prefixed duration and arguably the precomputed feedback gain)?

Response (8): We thank the reviewer for raising these important and technically insightful points regarding our modeling framework. We first clarify the structure of the model and key assumptions, and then address the specific questions in points (a)–(c) below.

We used Todorov’s (2005) stochastic optimal control method to compute a finite-horizon LQG policy under sensory noise and signal-dependent motor noise (state noise set to zero). The cost function is: <a href="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-2.jpg"><img src="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-2.jpg"></a> (see details in updated Methods). The resulting time-varying gains {Lk, Kk} correspond to the feedforward mapping and the feedback correction gain, respectively. The control law can be expressed as:

where uk is the control input, <a href="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-4.jpg"><img src="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-4.jpg"></a> is the nominal planned state, <a href="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-5.jpg"><img src="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-5.jpg"></a> is the estimated state, Lk is the feedforward (nominal) control associated with the planned trajectory, and Kk is the time-varying feedback gain that corrects deviations from the plan.

To define the motor plan for comparison with behavior, we simulate the deterministic open-loop

trajectory by turning off noise and disabling feedback corrections, i.e., <a href="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-6.jpg"><img src="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-6.jpg"></a>. In this framework, “feedforward” refers to this nominal motor plan. Thus, sensory and signal-dependent noise influence the computed policy (via the gains), but are not injected when generating the nominal trajectory. This mirrors the minimum-jerk practice used to obtain nominal kinematics in prior utility-based work (Shadmehr, 2016), while optimal control provides a more physiologically grounded nominal plan. In the revision, we have updated the equations, provided more modeling details, and moved the model description to the main text to reduce possible confusions.

In the implementation of the “mass underestimation” condition, the mass used to compute the policy is the underestimated mass (<a href="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-7.jpg"><img src="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-7.jpg"></a>), whereas the actual mass is used when simulating the feedforward trajectories. Corrective submovements are analyzed separately and are not required for the planning-deficit findings reported here.

Answers of the three specific questions:

a) We mistakenly wrote a continuous-time infinite-horizon cost function in our original manuscript, whereas our controller is actually implemented as a discrete-time finite-horizon LQG with a terminal cost, over a horizon set by the utility-based optimal movement duration Topt. The underestimated mass is used in both the utility model (to determine Topt) and in the control computation (i.e., internal model), while the true mass is used when simulating the movement. This mismatch captures the central idea of feedforward planning based on an incorrect internal model.

b) As described, our model includes signal-dependent motor noise and sensory noise, following Todorov (2005). We also evaluated whether increased noise levels in microgravity could account for the observed behavioral changes. Simulation results showed that increasing either source of noise did not alter the main conclusions or reverse the trends in our key metrics. Moreover, our experimental data showed no significant increase in endpoint variability in microgravity (see analyses and results in Figure 2—figure supplement 3 & 4), making it unlikely that increased sensorimotor noise alone accounts for the observed slowing and submovement changes.

c) In our framework, the time-varying gains {LK,KK}define the feedforward and feedback components of the control policy. While both gains are computed based on a stochastic optimal control formulation (including noise), for comparison with behavior we simulate only the nominal feedforward plan, by turning off both noise and feedback: <a href="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-6.jpg"><img src="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-6.jpg"></a>. This defines a deterministic open-loop trajectory, which we use to capture planning-level effects such as peak timing shifts under mass underestimation. Feedback corrections via gains exist in the full model but are not involved in these specific analyses. We clarified this modeling choice and its behavioral relevance in the revised text.

We have updated the equations and moved the model description into the main text in the revised manuscript to avoid confusion.

(3) Brevity of movements and speed-accuracy trade-off
The tested movements are much faster (average duration approx. 350 ms) than similar self-paced movements that have been studied in other works (e.g., Wang et al., J Neurophysiology, 2016; Berret et al., PLOS Comp Biol, 2021, where movements can last about 900-1000 ms). This is consistent with the instructions to reach quickly and accurately, in line with a speed-accuracy trade-off. Was this instruction given to highlight the inertial effects related to the arm's anisotropy? One may however, wonder if the same results would hold for slower self-paced movements (are they also with reduced speed compared to Earth performance?). Moreover, a few other important questions might need to be addressed for completeness: how to ensure that astronauts did remember this instruction during the flight? (could the control group move faster because they better remembered the instruction?). Did the taikonauts perform the experiment on their own during the flight, or did one taikonaut assume the role of the experimenter?

Response (9): Thanks for highlighting the brevity of movements in our experiment. Our intention in emphasizing fast movements is to rigorously test whether movement is indeed slowed down in microgravity. The observed prolonged movement duration clearly shows that microgravity affects people’s movement duration, even when they are pushed to move fast. The second reason for using fast movement is to highlight that feedforward control is affected in microgravity. Mass underestimation specifically affects feedforward control in the first place, shown by the microgravity-related changes in peak velocity/acceleration. Slow movement would inevitably have online corrections that might obscure the effect of mass underestimation. Note that movement slowing is not only observed in our speed-emphasized reaching task, but also in whole-arm pointing in other astronauts’ studies (Berger, 1997; Sangals, 1999), which have been quoted in our paper. We thus believe these findings are generalizable.

Regarding the consistency of instructions: all our experiments conducted in the Tiangong space station were monitored in real time by experimenters in the control center located in Beijing. The task instructions were presented on the initial display of the data acquisition application and ample reading time was allowed. All the pre-, in-, and post-flight test sessions were administered by the same group of personnel with the same instruction. It is common that astronauts serve both as participants and experimenters at the same time. And, they were well trained for this type of role on the ground. Note that we had multiple pre-flight test sessions to familiarize them with the task. All these rigorous measures were in place to obtain high-quality data. In the revision, we included these experimental details for readers that are not familiar with space studies, and provided the rationales for emphasizing fast movements.

Citations:

Berger, M., Mescheriakov, S., Molokanova, E., Lechner-Steinleitner, S., Seguer, N., & Kozlovskaya, I. (1997). Pointing arm movements in short- and long-term spaceflights. Aviation, Space, and Environmental Medicine, 68(9), 781–787.

Sangals, J., Heuer, H., Manzey, D., & Lorenz, B. (1999). Changed visuomotor transformations during and after prolonged microgravity. Experimental Brain Research. Experimentelle Hirnforschung. Experimentation Cerebrale, 129(3), 378–390.

(4) No learning effect
This is a surprising effect, as mentioned by the authors. Other studies conducted in microgravity have indeed revealed an optimal adaptation of motor patterns in a few dozen trials (e.g., Gaveau et al., eLife, 2016). Perhaps the difference is again related to single-joint versus multi-joint movements. This should be better discussed given the impact of this claim. Typically, why would a "sensory bias of bodily property" persist in microgravity and be a "fundamental constraint of the sensorimotor system"?

Response (10): We believe that the presence or absence of adaptation between our study and Gaveau et al.’s study cannot be simply attributed to single-joint versus multi-joint movements. Their adaptation concerned incorporating microgravity into movement control to minimize effort, whereas ours concerned accurately perceiving body mass. Gaveau et al.’s task involved large-amplitude vertical reaching, a scenario in which gravity strongly affects joint torques and movement execution. Thus, adaptation to microgravity can lead to better execution, providing a strong incentive for learning. By contrast, our task consisted of small-amplitude horizontal movements, where the gravitational influence on biomechanics is minimal.

More importantly, we believe the lack of adaptation for mass underestimation is not totally surprising. When an inertial change is perceived (such as an extra weight attached to the forearm, as in previous motor adaptation studies), people can adapt their reaching within tens of trials. In that case, sensory cues are veridical, as they correctly signal the inertial perturbation. However, in microgravity, reduced gravitational pull and proprioceptive inputs constantly inform the controller that the body mass is less than its actual magnitude. In other words, sensory cues in space are misleading for estimating body mass. The resulting sensory bias prevents the sensorimotor system from adapting. Our initial explanation on this matter was too brief; we expanded it in the revised Discussion.

Reviewer #3 (Public review):
Summary:
The authors describe an interesting study of arm movements carried out in weightlessness after a prolonged exposure to the so-called microgravity conditions of orbital spaceflight. Subjects performed radial point-to-point motions of the fingertip on a touch pad. The authors note a reduction in movement speed in weightlessness, which they hypothesize could be due to either an overall strategy of lowering movement speed to better accommodate the instability of the body in weightlessness or an underestimation of body mass. They conclude for the latter, mainly based on two effects. One, slowing in weightlessness is greater for movement directions with higher effective mass at the end effector of the arm. Two, they present evidence for an increased number of corrective submovements in weightlessness. They contend that this provides conclusive evidence to accept the hypothesis of an underestimation of body mass.

Strengths:
In my opinion, the study provides a valuable contribution, the theoretical aspects are well presented through simulations, the statistical analyses are meticulous, the applicable literature is comprehensively considered and cited, and the manuscript is well written.

Weaknesses:
Nevertheless, I am of the opinion that the interpretation of the observations leaves room for other possible explanations of the observed phenomenon, thus weakening the strength of the arguments.
First, I would like to point out an apparent (at least to me) divergence between the predictions and the observed data. Figures 1 and S1 show that the difference between predicted values for the 3 movement directions is almost linear, with predictions for 90º midway between predictions for 45º and 135º. The effective mass at 90º appears to be much closer to that of 45º than to that of 135º (Figure S1A). But the data shown in Figure 2 and Figure 3 indicate that movements at 90º and 135º are grouped together in terms of reaction time, movement duration, and peak acceleration, while both differ significantly from those values for movements at 45º.
Furthermore, in Figure 4, the change in peak acceleration time and relative time to peak acceleration between 1g and 0g appears to be greater for 90º than for 135º, which appears to me to be at least superficially in contradiction with the predictions from Figure S1. If the effective mass is the key parameter, wouldn't one expect as much difference between 90º and 135º as between 90º and 45º? It is true that peak speed (Figure 3B) and peak speed time (Figure 4B) appear to follow the ordering according to effective mass, but is there a mathematical explanation as to why the ordering is respected for velocity but not acceleration? These inconsistencies weaken the author's conclusions and should be addressed.

Response (11): Indeed, the model predicts an almost equal separation between 45° and 90° and between 90° and 135°, while the data indicate that the spacing between 45° and 90° is much smaller than between 90° and 135°. We do not regard the divergence as evidence undermining our main conclusion since 1) the model is a simplification of the actual situation. For example, the model simulates an ideal case of moving a point mass (effective mass) without friction and without considering Coriolis and centripetal torques. 2) Our study does not make quantitative predictions of all the key kinematic measures; that will require model fitting, parameter estimation, and posture-constrained reaching experiments; instead, our study uses well-established (though simplified) models to qualitatively predict the overall behavioral pattern we would observe. For this purpose, our results are well in line with our expectations: though we did not find equal spacing between direction conditions, we do confirm that the key kinematic measures (Figure 2 and Figure 3 as questioned) show consistent directional trends between model predictions and empirical data. We added new analysis results on this matter: the directional effect we observed (how the key measures changed in microgravity across direction condition) is significantly correlated with our model predictions in most cases. Please check our detailed response (2) above. These results are also added in the revision.

We also highlight in the revision that our modeling is not to quantitatively predict reaching behaviors in space, but to qualitatively prescribe that how mass underestimation, but not the conservative control strategy, can lead to divergent predictions about key kinematic measures of fast reaching.

Then, to strengthen the conclusions, I feel that the following points would need to be addressed:
(1) The authors model the movement control through equations that derive the input control variable in terms of the force acting on the hand and treat the arm as a second-order low-pass filter (Equation 13). Underestimation of the mass in the computation of a feedforward command would lead to a lower-than-expected displacement to that command. But it is not clear if and how the authors account for a potential modification of the time constants of the 2nd order system. The CNS does not effectuate movements with pure torque generators. Muscles have elastic properties that depend on their tonic excitation level, reflex feedback, and other parameters. Indeed, Fisk et al. showed variations of movement characteristics consistent with lower muscle tone, lower bandwidth, and lower damping ratio in 0g compared to 1g. Could the variations in the response to the initial feedforward command be explained by a misrepresentation of the limbs' damping and natural frequency, leading to greater uncertainty about the consequences of the initial command? This would still be an argument for unadapted feedforward control of the movement, leading to the need for more corrective movements. But it would not necessarily reflect an underestimation of body mass.
Fisk, J. O. H. N., Lackner, J. R., & DiZio, P. A. U. L. (1993). Gravitoinertial force level influences arm movement control. Journal of neurophysiology, 69(2), 504-511.

Response (12): We agree that muscle properties, tonic excitation level, proprioception-mediated reflexes all contribute to reaching control. Fisk et al. (1993) study indeed showed that arm movement kinematics change, possibly owing to lower muscle tone and/or damping. However, reduced muscle damping and reduced spindle activity are more likely to affect feedback-based movements. Like in Fisk et al.’s study, people performed continuous arm movements with eyes closed; thus their movements largely relied on proprioceptive control. Our major findings are about the feedforward control, i.e., the reduced and “advanced” peak velocity/acceleration in discrete and ballistic reaching movements. Note that the peak acceleration happens as early as approximately 90-100ms into the movements, clearly showing that feedforward control is affected -- a different effect from Fisk et al’s findings. It is unlikely that people “advanced” their peak velocity/acceleration because they feel the need for more later corrective movements. Thus, underestimation of body mass remains the most plausible explanation.

(2) The movements were measured by having the subjects slide their finger on the surface of a touch screen. In weightlessness, the implications of this contact are expected to be quite different than those on the ground. In weightlessness, the taikonauts would need to actively press downward to maintain contact with the screen, while on Earth, gravity will do the work. The tangential forces that resist movement due to friction might therefore be different in 0g. This could be particularly relevant given that the effect of friction would interact with the limb in a direction-dependent fashion, given the anisotropy of the equivalent mass at the fingertip evoked by the authors. Is there some way to discount or control for these potential effects?

Response (13): We agree that friction might play a role here, but normal interaction with a touch screen typically involves friction between 0.1N and 0.5N (e.g., Ayyildiz et al., 2018). We believe that the directional variation of the friction is even smaller than 0.1N. It is very small compared to the force used to accelerate the arm for the reaching movement (10N-15N). Thus, friction anisotropy is unlikely to explain our data. Indeed, our readers might have the same concern, we thus added some discussion about possible effect of friction.

Citation: Ayyildiz M, Scaraggi M, Sirin O, Basdogan C, Persson BNJ. Contact mechanics between the human finger and a touchscreen under electroadhesion. Proc Natl Acad Sci U S A. 2018 Dec 11;115(50):12668-12673.

(3) The carefully crafted modelling of the limb neglects, nevertheless, the potential instability of the base of the arm. While the taikonauts were able to use their left arm to stabilize their bodies, it is not clear to what extent active stabilization with the contralateral limb can reproduce the stability of the human body seated in a chair in Earth gravity. Unintended motion of the shoulder could account for a smaller-than-expected displacement of the hand in response to the initial feedforward command and/or greater propensity for errors (with a greater need for corrective submovements) in 0g. The direction of movement with respect to the anchoring point could lead to the dependence of the observed effects on movement direction. Could this be tested in some way, e.g., by testing subjects on the ground while standing on an unstable base of support or sitting on a swing, with the same requirement to stabilize the torso using the contralateral arm?

Response (14): Body stabilization is always a challenge for human movement studies in space. We minimized its potential confounding effects by using left-hand grasping and foot straps for postural support throughout the experiment. We think shoulder stability is an unlikely explanation because unexpected shoulder instability should not affect the feedforward (early) part of the ballistic reaching movement: the reduced peak acceleration and its early peak were observed at about 90-100ms after movement initiation. This effect is too early to be explained by an expected stability issue. This argument is now mentioned in the revised Discussion.

The arguments for an underestimation of body mass would be strengthened if the authors could address these points in some way.

Recommendations for the authors:

Reviewing Editor Comments:
General recommendation
Overall, the reviewers agreed this is an interesting study with an original and strong approach. Nonetheless, there were significant weaknesses identified. The main criticism is that there is insufficient evidence for the claim that the movement slowing is due to mass underestimation, rather than other explanations for the increased feedback corrections. To bolster this claim, the reviewers have requested a deeper quantitative analysis of the directional effect and comparison to model predictions. They have also suggested that a 2-dof arm model could be used to predict how mass underestimation would influence multi-joint kinematics, and this should be compared to the data. Alternatively, or additionally, a control experiment could be performed (described in the reviews). We do realize that some of these options may not be feasible or practical. Ultimately, we leave it to you to determine how best to strengthen and solidify the argument for mass underestimation, rather than other causes.
As an alternative approach, you could consider tempering the claim regarding mass underestimation and focus more on the result that slower movements in microgravity are not simply a feedforward, rescaling of the movement trajectories, but rather, have greater feedback corrections. In this case, the reviewers feel it would still be critical to explain and discuss potential reasons for the corrections beyond mass underestimation.

We hope that these points are addressable, either with new analyses, experiments, or with a tempering of the claims. Addressing these points would help improve the eLife assessment.

Reviewer #1 (Recommendations for the authors):
(1) Move model descriptions to the main text to present modelling choices in more detail

Response (15): Thank you for the suggestion. We have moved the model descriptions to the main text to present the modeling choices in more detail and to allow readers to better cross-reference the analyses.

(2) Perform quantitative comparisons of the directional effect with the model's predictions, and add raw kinematic traces to illustrate the effect in more detail.

Response (16): Thanks for the suggestion, we have added the raw kinematics figure from a representative participant and please refer to Response (2) above for the comparisons of directional effect.

(3) Explore the effect of varying cost parameters in addition to mass estimation error to estimate the proportion of data explained by the underestimation hypothesis.

Response (17): Thank you for the suggestion. This has already been done—please see Response (1) above.

Reviewer #2 (Recommendations for the authors):
Minor comments:
(1) It must be justified early on why reaction times are being analyzed in this work. I understood later that it is to rule out any global slowing down of behavioral responses in microgravity.

Response (18): Exactly, RT results are informative about the absence of a global slowing down. Contrary to the conservative-strategy hypothesis, taikonauts did not show generalized slowing; they actually had faster reaction times during spaceflight, incompatible with a generalized slowing strategy. Thanks for point out; we justified that early in the text.

(2) Since the results are presented before the methods, I suggest stressing from the beginning that the reaching task is performed on a tablet and mentioning the instructions given to the participants, to improve the reading experience. The "beep" and "no beep" conditions also arise without obvious justification while reading the paper.

Response (19): Great suggestions. We now give out some experimental details and rationales at the beginning of Results.

(3) Figure 1C: The vel profiles are not returning to 0 at the end, why? Is it because the feedback gain is computed based on the underestimated mass or because a feedforward controller is applied here? Is it compatible with the experimental velocity traces?

Response (20): Figure. 1C shows the forward simulation under the optimal control policy. In our LQG formulation the terminal velocity is softly penalized (finite weight) rather than hard-constrained to zero; with a fixed horizon° the optimal solution can therefore end with a small residual velocity.

In the behavioral data, the hand does come to rest: this is achieved by corrective submovements during the homing phase.

(4) Left-skewed -> I believe this is right-skewed since the peak velocity is earlier.

Response (21): Yes, it should be right-skewed, thanks for point that out.

(5) What was the acquisition frequency of the positional data points? (on the tablet).

Response (22): The sampling frequency is 100 Hz. Thanks for pointing that out; we’ve added this information to the Methods.

(6) Figure S1. The planned duration seems to be longer than in the experiment (it is more around 500 ms for the 135-degree direction in simulation versus less than 400 ms in the experiment). Why?

Response (23): We apologize for a coding error that inadvertently multiplied the body-mass parameter by an extra factor, making the simulated mass too high. We have corrected the code, rerun the simulations, and updated Figures 1 and S1; all qualitative trends remain unchanged, and the revised movement durations (≈300–400 ms) are closer to the experimental values.

(7) After Equation 13: "The control law is given by". This is not the control law, which should have a feedback form u=K*x in the LQ framework. This is just the dynamic equations for the auxiliary state and the force. Please double-check the model description.

Response (24): Thank you for point this out. We have updated and refined all model equations and descriptions, and moved the model description from the Supplementary Materials to the main text; please see the revised manuscript.

Reviewer #3 (Recommendations for the authors):
(1) I have a concern about the interpretation of the anisotropic "equivalent mass". From my understanding, the equivalent mass would be what an external actor would feel as an equivalent inertia if pushing on the end effector from the outside. But the CNS does not push on the arm with a pure force generator acting at the hand to effectuate movement. It applies torque around the joints by applying forces across joints with muscles, causing the links of the arm to rotate around the joints. If the analysis is carried out in joint space, is the effective rotational inertia of the arm also anisotropic with respect to the direction of the movement of the hand? In other words, can the authors reassure me that the simulations are equivalent to an underestimation of the rotational inertia of the links when applied to the joints of the limb? It could be that these are mathematically the same; I have not delved into the mathematics to convince myself either way. But I would appreciate it if the authors could reassure me on this point.

Response (25): Thank you for raising this point. In our work, “equivalent mass” denotes the operational-space inertia projected along the hand-movement direction u, computed as:

This formulation describes the effective mass perceived at the end effector along a given direction, and is standard in operational-space control.

Although the motor command can be coded as either torque/force in the CNS, the actual executions are equivalent no matter whether it is specified as endpoint forces or joint torques, since force and torque are related by <a href="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-9.jpg"><img src="https://cdn.elifesciences.org/public-review-media/107472/v2/Author-response-image-9.jpg"></a>. For small excursions as investigated here, this makes the directional anisotropy in endpoint inertia consistent with the anisotropy of the effective joint-space inertia required to produce the same endpoint motion. Conceptually, therefore, our “mass underestimation” manipulation in operational space corresponds to underestimating the required joint-space inertia mapped through the Jacobian. Since our behavioral data are hand positions, using the operational-space representation is the most direct and appropriate way for modeling.

(2) I would also like to suggest one more level of analysis to test their hypothesis. The authors decomposed the movements into submovements and measured the prevalence of corrective submovements in weightlessness vs. normal gravity. The increase in corrective submovements is consistent with the hypothesis of a misestimation of limb mass, leading to an unexpectedly smaller displacement due to the initial feedforward command, leading to the need for corrections, leading to an increased overall movement duration. According to this hypothesis, however, the initial submovement, while resulting in a smaller than expected displacement, should have the same duration as the analogous movements performed on Earth. The authors could check this by analyzing the duration of the extracted initial submovements.

Response (26): We appreciate the reviewer’s suggestion regarding the analysis of the initial submovement duration. In our decomposition framework, each submovement is modeled as a symmetric log-normal (bell-shaped) component, such that the time to peak speed is always half of the component duration. Thus, the initial submovement duration is directly reflected in the initial submovement peak-speed time already reported in our original manuscript (Figure. 5F).

However, we respectfully disagree with the assumption that mass underestimation would necessarily yield the same submovement duration as on Earth. Under mass underestimation, the movement is effectively under-actuated, and the initial submovement can terminate prematurely, leading to a shorter duration. This is indeed what we observed in the data. Therefore, our reported metrics already address the reviewer’s proposal and support the conclusion that mass underestimation reduces the initial submovement duration in microgravity. Per your suggestion, we now added one more sentence to explain to the reader that initial submovement peak-speed time reflect the duration of the initial submovement.

Some additional minor suggestions:
(1) I believe that it is important to include the data from the control subjects, in some form, in the main article. Perhaps shading behind the main data from the taikonauts to show similarities or differences between groups. It is inconvenient to have to go to the supplementary material to compare the two groups, which is the main test of the experiment.

Response (27): Thank you for the suggestion. For all the core performance variables, the control group showed flat patterns, with no changes across test sessions at all. Thus, including these figures (together with null statistical results) in the main text would obscure our central message, especially given the expanded length of the revised manuscript (we added model details and new analysis results). Instead, following eLife’s format, we have reorganized the Supplementary Material so that each experimental figure has a corresponding supplementary figure showing the control data. This way, readers can quickly locate the control results and directly compare them with the experimental data, while keeping the main text focused.

(2) "Importantly, sensory estimate of bodily property in microgravity is biased but evaded from sensorimotor adaptation, calling for an extension of existing theories of motor learning." Perhaps "immune from" would be a better choice of words.

Response (28): Thanks for the suggestion, we edited our text accordingly.

(3) "First, typical reaching movement exhibits a symmetrical bell-shaped speed profile, which minimizes energy expenditure while maximizing accuracy according to optimal control principles (Todorov, 2004)." While Todorov's analysis is interesting and well accepted, it might be worthwhile citing the original source on the phenomenon of bell-shaped velocity profiles that minimize jerk (derivative of acceleration) and therefore, in some sense, maximize smoothness. Flash and Hogan, 1985.

Response (29): Thanks for the suggestion, we added the citation of minimum jerk.

(4) "Post-hoc analyses revealed slower reaction times for the 45° direction compared to both 90° (p < 0.001, d = 0.293) and 135° (p = 0.003, d = 0.284). Notably, reactions were faster during the in-flight phase compared to pre-flight (p = 0.037, d = 0.333), with no significant difference between in-flight and post-flight phases (p = 0.127)." What can one conclude from this?

Response (30): Although these decreases reached statistical significance, their magnitudes were small. The parallel pattern across groups suggests the effect is not driven by microgravity, but is more plausibly a mild learning/practice effect. We now mentioned this in the Discussion.

(5) "In line with predictions, peak acceleration appeared significantly earlier in the 45° direction than other directions (45° vs. 90°, p < 0.001, d = 0.304; 45° vs. 135°, p < 0.001, d = 0.271)." Which predictions? Because the effective mass is greater at 45º? Could you clarify the prediction?

Response (31): We should be more specific here; thank you for raising this. The predictions are the ones about peak acceleration timing (shown in Fig. 1H). We now modified this sentence as:

“In line with model predictions (Figure 1H), ….”.

(6) Figure 2: Why do 45º movements have longer reaction times but shorter movement durations?

Response (32): Appreciate your careful reading of the results. We believe this is possibly due to flexible motor control across conditions and trials, i.e., people tend to move faster when people react slower with longer reaction time. This has been reflected in across-direction comparisons (as spotted by the reviewer here), and it has also been shown within participant and across participants: For both groups, we found a significant negative correlation between movement duration (MD) and reaction time (RT), both across and within individuals (Figure 2—figure supplement 5). This finding indicates that participants moved faster when their RT was slower, and vice versa. This flexible motor adjustment, likely due to the task requirement for rapid movements, remained consistent during spaceflight.